Do unemployed workers bene�t from enterprise zones?

The French experience

L. Gobillon�, T. Magnacy, H. Selodz

First version, December 2008This version: October 25, 2010

Abstract

This paper is a statistical evaluation of the 1997 enterprise zone program in France. We

investigate whether the program increased the pace at which unemployed workers residing in

targeted municipalities and surrounding areas �nd employment. The work relies on a two-

stage analysis of unemployment spells drawn from an exhaustive dataset over the 1993-2003

period in the Paris region. We �rst estimate a duration model strati�ed by municipalities in

order to recover semester-speci�c municipality e¤ects net of individual observed heterogene-

ity. These e¤ects are estimated both before and after the implementation of the program,

allowing us to construct variants of di¤erence-in-di¤erence estimators of the impact of the

program at the municipality level. Following extensive robustness checks, we conclude that

enterprise zones have a very small but signi�cant e¤ect on the rate at which unemployed

workers �nd a job. The e¤ect remains localized and is shown to be signi�cant only in the

short run.

�Institut National d�Etudes Démographiques, PSE and CREST. Address: INED, 133 boulevard Davout, 92245

Paris Cedex, France. E-mail: laurent.gobillon@ined.fr.yToulouse School of Economics, Université de Toulouse (GREMAQ & IDEI) Address: Manufacture des Tabacs,

21 allée de Brienne, 31000 Toulouse, France. E-mail: magnac@cict.fr.zThe World Bank, Paris School of Economics and CREST. Address: The World Bank, Development Economics

Research Group, 1818 H Streeet, NW, Washington, DC 20433, USA. E-mail: hselod@worldbank.org.

1

1 Introduction1

Most cities have distressed neighborhoods where jobs are few and unemployment is rampant. As

a response, considering that the lack of labor demand in poor areas is a key contributor to un-

employment, a number of countries �including the US, the UK and France�have implemented

spatially targeted policies to encourage job creation or job relocation to these areas. Such poli-

cies �often labelled enterprise zone programs (EZ hereafter)�revolve around the simple idea that

granting �scal incentives to �rms located in distressed neighborhoods would boost local hires. Al-

though intuitively appealing, enterprise zones are controversial as many observers have questioned

their ability to reach their objectives and whether achieved bene�ts are su¢ cient to balance costs

(Peters and Fishers, 2004).

The goal of the present paper is to provide an econometric evaluation of the French experience

in this domain, focusing on the Paris region for which there exists a dataset that allows an adequate

evaluation of the policy at the municipality level. The key measure in the French program is that,

in order to be exempted from the wage tax, �rms needed to hire at least 20% of their labor force

locally (after the third hired worker). In the French context, this is a signi�cant incentive as the

wage tax exemption is larger than a third of all labor costs borne by employers depending on the

wage level and type of worker. The policy was expected to improve local employment through

hires made by existing, relocating, or newly-created �rms that would draw from the local pool of

unemployed workers.

Our approach for the impact evaluation of the program is original in various ways.

1The authors are grateful to participants at the following conferences and seminars: NARSC �08, EALE �09,

ESEM �09, and London School of Economics, for their helpful comments, and particularly to Shawn Rohlin, Je¤rey

Zax and Roland Rathelot. They would also like to thank the French Ministry of Health (MiRe-DREES) and the

French Ministry of Labor (DARES) for �nancial support. The opinions expressed in this article are those of the

authors and do not necessarily re�ect the views of our employers, including the World Bank, its Executive Board,

or the countries represented. All remaining errors are ours.

2

First, we depart from the approach used in previous papers in the literature as we investigate

the propensity of local unemployed workers to �nd a job. In the past, evaluations of enterprise

zones usually focused on the growth in the local number of establishments or on the number of

local jobs that were created as a result of the policy. Nonetheless, using job creation as a measure

of policy outcome misses part of the story as it is usually impossible to tell whether job creations

bene�t local residents or residents from non-targeted areas. Instead, in the present paper, we

investigate how the policy a¤ects the �ow out of unemployment, distinguishing between locations.

This is a more appropriate indicator of policy success given the explicit policy goal of helping

unemployed workers residing in distressed areas �nd jobs.

Second, focusing on unemployment duration has the advantage of capturing the overall local

e¤ect of job creations on the propensity to �nd a job. Indeed, policy evaluations that focus exclu-

sively on job creations in new establishments are likely to provide a biased estimate of the e¤ect

by overlooking the fact that jobs may also be created in existing �rms or that there could be some

substitution of jobs between existing �rms and new establishments. Focusing on unemployment

duration eliminates these problems.

Third, we propose a new econometric methodology that allows for a �ne estimation of the pol-

icy�s local e¤ects while controlling for the composition of the sample in each location, thus avoiding

composition bias in the estimation. We use a two-stage procedure, which revolves around the esti-

mation of a proportional hazard model of individual unemployment durations which is strati�ed by

municipality and which controls for individual characteristics. In the �rst stage, we use the Strat-

i�ed Partial Likelihood Estimator (SPLE) proposed by Ridder and Tunali (1999) and compute

spatial e¤ects for each of the 1,300 municipalities that form the Paris region. These municipality

e¤ects are purged of the e¤ects of individual observed characteristics for each semester between

1993 and 2003 and capture all municipality characteristics that have an impact on unemployment

duration. Right censoring that a¤ects unemployment durations is also controlled for. In a second

3

stage, in order to assess the e¤ect of the policy, we measure how these municipality e¤ects changed

over time (before and after the creation of enterprise zones) comparing municipalities that host an

enterprise zone �the "treated" municipalities�and other municipalities of comparable characteris-

tics. This second stage uses matching and di¤erences in di¤erences techniques to address possible

issues of treatment selectivity.

Fourth, we use a large number of localities (i.e. 1,300) for the strati�cation in the estimation

of the unemployment duration model. A municipality corresponds to the �nest spatial unit of

analysis that is available in the data. Since municipalities have a population size which is broadly

twice that of the enterprise zone they contain, this means that we capture net e¤ects in the EZ

and non-EZ parts of a same municipality only. Since municipalities are relatively small, however,

we are able to investigate the possibility of spatial spillovers on neighboring municipalities.

Finally, our work complements the only existing econometric study of enterprise zone programs

in France, which found only a limited impact on the growth in the number of establishments (see

Rathelot and Sillard, 2009).

Our core approach to estimate the e¤ect of the policy contrasts exit rates from unemployment

between municipalities which are selected for the policy and municipalities in a comparison group

around the date of implementation of the policy. Several methods were at our disposal in the

toolkit of evaluation methods (see Blundell and Costa-Dias, 2009, for a recent survey). Because

the sample we are considering is small, we resort to a linear model rather using non-parametric

methods. Second, in the absence of a controlled experiment, the key was the construction of

the comparison, or control group, in a very careful way (Smith and Todd, 2005). In the French

experience, zone designation was based on a criterion that included measures of population and

labor force composition. Political tampering implied that the municipalities that were not targeted

by the program but have characteristics similar to those of treated municipalities can be used as

a control group. To match municipalities, we started by estimating the propensity score �i.e. the

4

probability of being chosen as an enterprise zone municipality �as a function of the same variables

that were o¢ cially used to construct an eligibility criterion in the French enterprise zone program.

Based on this propensity score, we then constructed a control group of municipalities whose

propensity score is in the same range as that of treated municipalities, ensuring that municipalities

in both groups share the same conditions. However, the data clearly tell that the set of variables

included in the eligibility criterion is not rich enough to account for the heterogeneity in outcomes

between treated and control municipalities (Smith and Todd, 2005). Conditioning on municipality

geographic conditions was thus also necessary. This is why we ended up using a di¤erence in

di¤erences approach combined with matching on a propensity score (Heckman, Ichimura and

Todd, 1997). The results of our empirical strategy prove to be robust to a variety of appropriate

robustness checks relative to rede�nitions of treatment and control so as to capture spillover e¤ects,

to various weighting schemes or to the introduction of other controlling factors.

Our results point to three important conclusions for public policy. First, we �nd evidence

that the policy tended to "pick winners", that is to select municipalities in which unemployed

workers face better prospects, a common feature in many EZ programs. More importantly, we

�nd that enterprise zones have a moderate (3%) but signi�cant impact on unemployment exit

rates to employment in the short run (at most 3 years). We do not �nd evidence of medium run

e¤ects (between 3 and 6 years) although this could potentially be attributed to the failure of the

common trend assumption underlying di¤erence-in-di¤erence estimation. Finally, the e¤ect on

unemployment exits remains localized and no spillover e¤ects are signi�cant.

The structure of the paper is as follows. Following this introduction, we provide a survey of the

literature on enterprise zones in a second section. We present the French enterprise zone program

in a third section. We then describe our data in a fourth section. A �fth section explains our

estimation strategy, while a sixth section discusses the results of the policy evaluation. A seventh

section concludes and o¤ers a policy discussion.

5

2 Enterprise zones: a survey of the literature

Enterprise zones (EZ) programs are territorial discrimination policies that consist in providing tax

incentives and exemptions from regulations to speci�c blighted areas. The objective is to promote

local economic development and, in particular, to improve the level of local employment through

incentives for �rms to invest, hire, locate or relocate to the targeted areas. The concept, which

was initially inspired by the rapid development of free trade zones in the early 1970s in emerging

economies, was �rst used as a tool for urban policy by the United Kingdom in 1981. In the wake

of the UK initiative, several US states also enacted similar legislations, starting with Connecticut.

Furthermore, a US federal program of empowerment zones was implemented in several cities in

1994. It provided not only tax incentives to the �rms but also important social service block

grants�i.e. lump sum transfers from the federal government to States that are spent on targeted

areas. Following these experiences, France voted its �rst EZ program in 1996.

A comparison of existing EZ programs shows that the speci�c �scal tools that are used vary

widely from di¤erent forms of relief on capital taxation to employment and hiring tax credits, or a

combination of both. The speci�c tools may also vary depending on the zone designation process,

the conditionality for tax credit eligibility, the intensity and scope of the tax credits, the duration

and phasing out of the exemptions, the time frame of the program, the spatial coverage and the

number of zones, the requirement to simultaneously implement a local urban development plan,

or whether foregone local tax revenues are partially or completely compensated by the State.

In theory, enterprise zone programs are expected to contribute to local economic development

through several mechanisms depending on the speci�c features of the program and the context. In

what follows, we will focus on whether they can succeed in promoting employment. The e¤ect of

capital subsidies is ambiguous. Although capital subsidies (like e.g. credit on local property tax,

or tax credit on inventories) should encourage investments, this could happen at the expense of

employment if capital and labor are substitutes in production (Lynch and Zax, 2008). In the case

6

of factor complementarity, however, capital subsidies could be expected to have a positive e¤ect

also on employment. As for labor subsidies (like e.g. relief on wage taxes), they should have an

unambiguous e¤ect on employment by strengthening the incentives to hire workers. Income tax

rebates should encourage both hiring and investments.

Despite the mechanisms just described, several criticisms grounded in economic theory have

been formulated. A �rst issue is that �scal incentives may only turn out to provide windfall

e¤ects to �rms who would have hired workers in any case, with little impact on the local level

of employment. But then, conditioning the tax credits on local hiring� as it is often the case

in enterprise zone programs� should address this problem and improve employment, at least in

targeted areas. Another related issue is that enterprise zones may not necessarily result in job

creation but could cause geographical shifts in jobs from non-EZ to EZ areas. However, even if

it turns out to be the case, it is not clear whether this should be considered a failure of the

policy as it can be socially desirable to spatially redistribute jobs to places of low employment,

even in the case of a zero-sum game. A third argument is that zone designation may result in

the stigmatisation of the targeted neighborhood, further exacerbating the redlining behavior of

employers. The issue is then whether the adverse indirect e¤ect of stigmatisation outweighs the

expected direct bene�cial impact on employment. A fourth objection stresses that in the absence of

tax revenue compensation, enterprise zone programs may lead to a decrease in the local provision

of public services, which in turn could have a detrimental e¤ect on employment� and in any

case on the welfare of the local population. Of course, this depends on the way the EZ program

and infrastructures are funded. The problem can be addressed by ensuring that the enterprise

zone legislation provides appropriate mechanisms for compensation or can be avoided altogether

if the burden of the tax cuts is directly borne by the State and not by the local government.

Moreover, a �fth criticism argues that the e¤ects of enterprise zones could be only transitory and

will cease with the phasing out of the exemptions. As a matter of fact, in many cases, exemptions

7

have been extended passed the initial deadline� although this may involve the perpetuation of a

costly policy. Lastly, it can be argued that providing only �scal incentives could be insu¢ cient to

improve local employment when unemployment is structural as is the case for instance when there

is a mismatch between unemployed workers�skills and job requirements. This argues in favor of

integrated policies beyond the sole stimulation of labor demand.

In view of these arguments, whether enterprise zones successfully manage to improve employ-

ment may strongly depend on the speci�city of each program and on the local context. This clearly

makes the evaluation of EZ programs a key empirical matter for policy makers and explains the

relatively abundant literature on the topic (see Ladd, 1994, Peters and Fisher, 2004, and Hira-

suna and Michael, 2005, for surveys). It is only in the mid 1990s however that proper evaluations

started to emerge, resorting to a variety of statistical techniques and focusing on a variety of labor-

market indicators.2 The main usual challenge in such evaluations is to address selection issues.

Areas are often selected according to a ranking using some economic indicator as well as on possi-

ble political tampering from local government representatives seeking bene�t from the policy for

their constituencies. Addressing this issue thus requires resorting to quasi-experimental techniques

using panel data to control for local heterogeneity. Identi�cation strategies typically range from

random growth models to di¤erence in di¤erences, possibly using propensity score matching to

de�ne adequate control groups or propensity score reweighting to construct some counterfactuals.

In the US, the econometric evaluations of state EZ programs reported in the economic literature

provide mixed results. To our knowledge, the �rst such study is Papke (1994) who evaluates the

e¤ect of the 1983 Indiana enterprise zone program, which consisted in providing credits to �rms on

the local property and inventory tax� as well as in granting residents an income tax deduction� in

a selection of areas in central cities. The author�s main �nding is that annual local unemployment

2Many past evaluations undertaken before the mid 1990s, did not apply the now-standard techniques of public

policy evaluation. In some cases, evaluations were not carried out by parties external to the program. This resulted

in a controversial literature with sometimes unclear and contradictory results.

8

claims declined by a surprisingly high 19% following zone designation. Given the modesty of

employment incentives in the program, the author suggests that this result may re�ect some

"demonstration e¤ect" as was indeed described by zone administrators. Elvery (2009) studies the

EZ programs in California and Florida and �nds no evidence that enterprise zones have a¤ected

the individual probability of employment for zone residents. Focusing on the 1984 New Jersey

program, Boarnet and Bogart (1996) look at the number of job creations in municipalities with

an enterprise zone. As they do not �nd any e¤ect, they speculate that this could be due to a shift

in jobs from non-EZ to EZ areas within the concerned municipalities.

These contrasting results raise the issue that some enterprise zone policies may be more successful

than others. This is tested by Bondonio and Engberg (2000) who assess the e¤ect of enterprise zone

programs in �ve di¤erent states3 on local employment at the ZIP-code level while also controlling

for the monetary value of the incentives. They �nd very little impact on the di¤erence between non-

EZ and EZ employment growth. Like Boarnet and Bogart, they suspect that this weak aggregate

e¤ect could be due to job transfers from non-EZ to EZ areas within the same ZIP-code area and

from old to new �rms within the same ZIP-code area. The latter argument is consistent with

the idea that start-ups could drive away existing businesses during the implementation of the

program.

To further estimate the dynamics at work beyond the average impact estimated in previous studies,

Bondonio and Greenbaum (2007) focus on the e¤ects of enterprise zone programs in ten states4 and

Washington, DC. Their approach consists in separately evaluating the e¤ects of the EZ program

on new, existing and vanishing establishments. Consistently with Bondonio and Engberg (2000)�s

intuition, they �nd that enterprise zone programs increase employment in new establishments

but that this is o¤set by the accelerated loss of employment in vanishing establishments. They

3California, Kentucky, New York, Pennsylvania and Virginia.4California, Connecticut, Florida, Indiana, Kentucky, Maryland, New Jersey, New York, Pennsylvania, and

Virginia.

9

are also able to identify which features of the programs have greater positive impacts on existing

businesses, stressing the role of incentives tied to job creation and of strategic local development

plans.

O�Keefe (2004) investigates two other issues concerning enterprise zone programs: whether possible

e¤ects on employment are transitory or permanent, and whether wage tax credits are captured

by higher wages. Using annual establishment-level employment data at the census tract level

between 1992 and 1999 in California� where the enterprise zone program provides hiring credit

for low wages to be phased out after six years� she �nds that employment in targeted zones grew

3.1 percent faster the �rst six years after designation than it would have in the absence of the

program. But the e¤ect is only transitory. She suggests that the waning of the e¤ect could be

explained by the phasing out of the hiring incentive, and also by the reduced availability of vacant

properties for businesses and �rms in the zone as the years pass. As for wages, they do not seem to

be a¤ected by the enterprise zone program. Nonetheless, these �ndings on the California program

have been challenged by other studies. The results on employment are contradicted by Neumark

and Kolko (2010) who use the precise street boundaries of enterprise zones and check whether

establishments are located within these boundaries over the 1992-2004 period. They �nd that

the e¤ect of enterprise zones on employment is insigni�cant both in the short and the long run.

O�Keefe�s results on wages are also contradicted by Bostic and Prohofsky (2006) who show, using

administrative �scal data, that the income of enterprise zone participants in California increased

more rapidly than for controls.

Since 1994, a federal "empowerment zone" program has complemented the enterprise zone

policies that were initiated by states. This program created empowerment zones in six urban

communities5 where local �rms were granted substantial tax credits for each employee living and

working in the concerned areas. Empowerment zones also became eligible for important block grant

5Atlanta, Baltimore, Chicago, Detroit, New York City, and Philadelphia/Camden.

10

funds from the federal government which could be used for social purposes. Other policy measures

included grants meant to facilitate large-scale physical development projects, tax-exempt bonds to

businesses, and write-o¤s from taxes (see Busso and Kline, 2008 for more details). Evaluations of

the e¤ects of the federal program on labour market performances are reported in several studies. In

particular, Busso and Kline (2008) compare census tracts in designated zones with tracts including

rejected zones or which ended up designated only at a later date. They �nd that EZ programs had

a positive e¤ect on local employment and a negative e¤ect on the local poverty rate. Their results

on employment and poverty are debated by Hanson (2009) who argues that EZ designation might

have been endogenous. When instrumenting EZ designation by political variables, he �nds that

EZ programs had no e¤ect on employment and poverty.

3 Enterprise zones in France

France launched its �rst enterprise zone program on January 1, 1997 by creating 44 enterprise zones

(Zones Franches Urbaines in French), among which 38 are located in metropolitan France, and 9

in the Paris region.6 Enterprise zones are the smallest level of a nested three-tier zoning system of

distressed areas around which France organizes its urban policy interventions. While the �rst and

second tier (the Zones Urbaines Sensibles and Zones de Redynamisation Urbaine respectively) are

mostly the focus of social programs and urban revitalization projects, the third tier� which groups

areas that are most distressed� was only de�ned for the speci�c implementation of the French EZ

program (see Observatoire National des Zones Urbaines Sensibles, 2004, for more details). Since

6The 9 targeted neighborhoods in the Paris region are located within or across 13 municipalities. The list is as

follows: Beauval / La Pierre Collinet (in the municipality of Meaux), Zup de Surville (in Montereau-Fault-Yonne),

Le Val Fourré (in Mantes-la-Jolie), Cinq Quartiers (in Les Mureaux), La Grande Borne (in Grigny and Viry-

Châtillon), Quartier Nord (in Bondy), Grand Ensemble (in Clichy-sous-Bois and Montfermeil), Le Bois L�Abbé /

Les Mordacs (in Champigny-sur-Marne and Chennevières-sur-Marne), Dame Blanche Nord-Ouest / La Muette /

Les Doucettes (in Garges-lès-Gonesse and Sarcelles).

11

the number and intensity of �scal exemptions is gradually increased when comparing the �rst,

the second, and the third tiers of urban interventions, EZs bene�t from the complete set of �scal

incentives.

As is well known in France, the selection of enterprise zones was clearly not random. Municipal-

ities or groups of municipalities had to apply to the program and projects were selected according

to their ranking given by a synthetic indicator. This indicator aggregates 5 criteria based on the

population of the zone, its unemployment rate, the proportion of youngsters, the proportion of

workers with no skill, and the so-called ��scal potential�of the municipality or municipalities in

which the zone is located.7 Nevertheless, the views of local and centralized government represen-

tatives who intervened in the geographic delimitation of the zones were also taken into account.

After application of the criteria and consideration of local interests, enterprise zones ended up be-

ing large neighborhoods of at least 10,000 inhabitants that had particularly severe unemployment

problems.

Figures from the 1999 Census of the Population (the closest year to the designation date) indicate

that 730,000 people, around 1.25% of the French population at that time, resided in these zones.

The nine enterprise zones in the Paris region hosted almost 220,000 inhabitants, i.e. 2% of the

population of the region. They also accounted for a signi�cant portion of the population in the

municipalities where they are located (between 22 and 68%, and 45% on average).

The �scal incentives were uniform across the country and consisted in a series of tax reliefs on

property holding, corporate income, and in particular wages (see DARES, 2004, for more details).8

7The ��scal potential� is the �ctive local amount of taxes that would be collected if tax rates were uniform

across all municipalities in France. The formula for the synthetic indicator is the product of the �rst four criteria

divided by the �fth (see DIV, Observatoire National des Zones Urbaines Sensibles, 2004).8Exemptions concern the speci�c following taxes: charges sociales patronales (employers�social security con-

tribution which constitutes the �wage tax�), taxe professionnelle (business rate), impôt sur les béné�ces (pro�t

tax), taxe foncière (property tax), and cotisations sociales personnelles maladie et maternité (individual health

insurance contributions).

12

The key measure was that �rms needed to hire at least 20% of their labor force locally (after the

third worker hired) in order to be exempted from the wage tax (mainly employers�contribution to

national insurance). These exemptions were meant to be temporary and were more advantageous

for small �rms (i.e. establishments with less than 5 salaried workers) which bene�ted from a

9-year rather than a 5-year exemption completed by a 3 year degressive exemption. The program

was meant to last until January 1, 2002, but exemptions were extended beyond that date. At that

time, they were also slightly modi�ed and the local employment threshold was increased to 33%.

In 2004, 41 new enterprise zones were created. In 2006, an additional 15 were added to the list.

Surprisingly, no evaluation of the French enterprise zone program was initially planned. Al-

though some �evaluations�based on descriptive statistics were subsequently carried out by di¤er-

ent public authorities, they yielded opposite conclusions from �no e¤ect�to �considerable e¤ects�

(DIV, 2001, André, 2002). Whereas descriptive statistics suggested that enterprise zones a¤ected

the local dynamics of job and establishment creations, they depicted a potentially ambiguous e¤ect

on unemployment. Between 1997 and 2001, the ratio of establishment openings to the initial stock

of establishments has been estimated at 236% in enterprise zones, compared to 76% in the rest of

the metropolitan areas where EZs are located (Ernst, 2008). Note however that these �gures are

gross establishment creations and do not take into account destructions. Interestingly, the 5-year

survival rates of establishments are quite similar in EZs and the rest of their metropolitan areas.

The increase in the number of establishments, however, may not fully percolate to an increase in

local employment because �rms in enterprise zones are typically very small. It has been calculated

for instance that 50% of hired workers in EZ�s in 2002 were hired by �rms of less than 10 salaried

workers, and that 15% of the �rms in EZs had no salaried worker at all (Thélot, 2004). Although

not a statistical evaluation of the EZ program, Gilli (2006) reports that between 1997 and 2002,

the number of jobs in the 38 metropolitan enterprise zones grew from 27,000 to 72,000. Even

though the increase seems large in relative terms, it is less drastic when compared to the resident

13

population. In fact, jobs remained scarce with respect to the size of the labor force. While there

were approximately 10 jobs for 100 labor force participants in EZs in 1997, the �gure only increased

to 13 jobs for 100 labor force participants in 2003. Although an improvement, this remains rather

small. In addition, 22% of job creations in EZs are believed to have resulted from the relocations

of �rm which may have brought some workers with them.

Although these �gures are interesting per se, they do not constitute an assessment of the e¤ects of

the French enterprise zone program. To our knowledge, the only existing econometric evaluation

of enterprise zones is Rathelot and Sillard (2009) who focus on the e¤ect of enterprise zones on

establishment creation and salaried employment. Their identi�cation strategy takes advantage of

the transformation of a number of community redevelopment areas (Zones de Redynamisation

Urbaines) into enterprise zones (Zones Franches Urbaines) in 2004 when the second wave of

enterprise zones was enacted. Using di¤erence in di¤erences techniques, they �nd that enterprise

zones had only a modest e¤ect on establishment creation and salaried jobs (possibly 4,000 jobs

between 2004 and 2006 for the whole country).

Our study departs from Rathelot and Sillard (2009) in two important respects. First, we focus

on the creation of the �rst wave of enterprise zones in 1997. This enables us to measure the

whole e¤ect of the enterprise zone creation rather than just an incremental e¤ect of the territorial

policy (an intensi�cation of the incentives provided to employers with the passage of the second

to the third tier of urban interventions). Secondly, we focus on the e¤ect of the policy on local

unemployment rather than on local jobs (which may partly bene�t non-residents). To this end,

we use individual data on unemployment rather than �rm data on employment.

4 The Data

We focus on the Paris region, which roughly corresponds to the Paris metropolitan area. With 10.9

million inhabitants, the region is subdivided into 1,300 municipalities including the 20 subdistricts

14

of the city of Paris. These municipalities have very di¤erent population sizes that range from

225,000 residents in the most populous Parisian subdistrict to small villages located some 80 km

away from the city center (Source: 1999 Census of the Population).

We use the historical �le of job applicants to the National Agency for Employment (Agence

Nationale pour l�Emploi or ANPE hereafter) for the Paris region. The sample includes all unem-

ployment spells ending in the period running from July 1993 to June 2003. This interval includes

the implementation date of the enterprise zone program (January 1, 1997) and is broad enough to

study the e¤ect of enterprise zones not only in the short run, but also in the medium run. It is an

almost exhaustive dataset of unemployment spells in the region given that registration with the

national employment agency is a prerequisite for unemployed workers to be able to claim unem-

ployment bene�ts in France. It contains information on the exact date of an application (the very

day), the unemployment duration in days, the reason for which the application came to an end,

the municipality where the individual resides, and a set of socio-economic characteristics reported

upon registration with the employment agency (age, gender, nationality, diploma, marital status,

number of children and disabilities).

We decided to focus on unemployment spells that began at most four years before July 1,

1993 (i.e. after July 1, 1989) and arti�cially censored the few spells which lasted longer than four

years. This is because the assumptions underlying our duration model are unlikely to be satis�ed

for very long spells. After eliminating the very few observations for which some socio-economic

characteristics are missing, we are able to reconstruct 8,831,456 unemployment spells ending in

the period between July 1, 1993 and June 30, 2003. These unemployment spells may end when the

unemployed �nd a job, drop out of the labor force, leave unemployment for an unknown reason

or when the spell is right censored. Given the focus of the paper, we will mainly study exits that

end with �nding a job, all other exits being treated as right-censoring in the analysis.

We �rst graphically describe the evolution of the variables of interest over the period of ob-

15

servation. We report in Figure 1 the unemployment rate in the region (from the Labour Force

Surveys) as well as the exit rate (to any destination) and the entry rate, both computed from

our data.9 As justi�ed later on, the time frequency that we use is the semester, with semester 1

corresponding to the second semester of 1993.

[Insert F igure 1]

In the period running from the second semester of 1996 (semester 7) to the �rst semester of 1999

(semester 12), there is no common trend for unemployment and exit rates since the unemployment

rate is rather �at while the exit rate is decreasing. Interestingly, the entry rate into unemploy-

ment follows the same decreasing pattern. Stable unemployment in this period is thus concealing

decreasing entry and exit rates. The period from the second semester of 1999 (semester 13) until

the �rst semester of 2001 (semester 16) exhibits a di¤erent pattern. Unemployment decreases

whereas both entry and exit rates increase. After the second semester of 2001 (semester 17), the

exit rate falls below the entry rate and unemployment increases.

To complete this description, Figure 2 reports the evolution of the di¤erent rates of exit from

unemployment by destination type, i.e. to a job, to non-employment or for unknown reasons. The

exit rate to non-employment is relatively constant. The exit rate to a job trends downwards around

the time the policy is implemented in the �rst semester of 1997 (semester 8). Note also that the

rate of exits for unknown reasons slightly increases after the second semester of 1999 (semester

13). It suggests that some rules may have changed at that time in the way exits are recorded and

9The entry rate is the number of new unemployed workers within the semester divided by the number of

unemployed workers at risk at the beginning of the semester. Since there are strong seasonal elements regarding

the entry rate, we graphed a moving average of order 2 so as to smooth the curve and make the graph more

readable. The exit rate to a given destination is the number of unemployed workers experiencing a transition to

this destination within the semester divided by the number of unemployed workers at risk at the beginning of the

semester.

16

in the empirical analysis below we will assess whether this change a¤ects the evaluation.

[Insert F igure 2]

Secondly, descriptive statistics on the number of unemployed workers at risk and the number

of exits to a job are reported by semester in Table 1 for the whole region (�rst two columns). The

number of unemployed workers at risk is nearly constant from 1993 to 1999 and then decreases

before increasing again in 2001. This is consistent with a sharp decrease in the unemployment rate

after 1999 as was seen in the above graphs. The number of exits to a job does not follow exactly

the same pattern as the decrease occurs sooner, in 1996, as seen in Figure 2.

[Insert Table 1]

Over the whole period, the proportion of exits to a job decreases from 11:2% to 7:2%:

We also reported in Table 1 the same statistics for municipalities which size is in the 8,000-

100,000 range as we will restrict our working sample to that range in the policy evaluation section.

This range contains all treated municipalities and comprises approximately 300 municipalities out

of the 1,300 in the Paris region. There are no noticeable di¤erences between this restricted sample

and the full sample. Roughly speaking an average of 90,000 persons �nd a job each semester and

this corresponds to about 300 exits per semester in each municipality. These �gures explain why

we chose semesters as the time intervals in our analysis since using shorter periods would imply

too much variability due to the small sample size.

The raw data used in the evaluation of the EZ program are described by Figures 3 to 6. Figure

3 reports the evolution of the exit rates in the sample of treated municipalities and in three control

groups: a sample composed by non-treated municipalities between 8,000 and 100,000, and two

subsamples of that group made of municipalities located at a distance between 0 and 5 kilometers

of an EZ, or between 5 and 10 kilometers. For readability, we drew a vertical line at semester 8

(�rst semester of 1997) when the policy started to be implemented. The curves for the control

17

groups are broadly decreasing and exhibit parallel trends throughout the period. The curve for the

treatment group slightly diverges from the trends observed for the control municipalities between

semesters 1 and 12 (second semester of 1993 to �rst semester of 1999). In particular, the exit

rate to a job remains �at in the treatment group between semesters 7 and 8 (second semester of

1996 and �rst semester of 1997) when the policy enters into e¤ect whereas it is decreasing in the

control groups. The estimation of the treatment parameter that we undertake in the remaining

sections of the paper is a way of formalizing and testing that these diverging trends are statistically

signi�cant.

None of these di¤erences seems to appear in graphs reporting the evolution of exit rates to non-

employment (Figure 4) and the evolution of exit rates for unknown reasons (Figure 5). In the latter

Figure, it is noticeable that exit rates for unknown reasons become larger in treated municipalities

the semester after the implementation of the treatment. However, our treatment parameter using

information on reported exits to a job would be underestimated only if a substantial fraction of

exits to a job are concealed among exits for unknown reasons. We attempt to estimate this e¤ect

later on and �nd that the apparent increase is spurious (see Table 15). In Figure 5, it is also

noticeable that censorship due to exit rates for unknown reasons increased between semesters 12

and 14 (�rst semester of 1999 and �rst semester of 2000), which is consistent with our previous

remarks on Figure 2.

Lastly, Figure 6 represents the evolution of exit rates to a job, distinguishing between two

groups of municipalities depending on the share of their population residing in the enterprise zone.

The "�attening" e¤ect between semester 7 (before treatment) and semester 8 (after treatment), as

already seen in Figure 3, is much more pronounced in municipalities in which the enterprise zone

host a larger fraction of the population. As a matter of fact, rates of exit to a job even increased

in those municipalities.

Turning to the composition of the sample before and after the beginning of policy implemen-

18

tation, we report in Tables 2 and 3 some descriptive statistics at two dates before and after the

creation of enterprise zones (we chose the �rst semester of 1994 and the �rst semester of 2000,

which de�nes a period over which the exit rates are decreasing). These Tables show that the

sample averages are close at the two dates. There are some slight di¤erences in gender composi-

tion though as the proportion of females in the sample increases from 49:1% in 2000 to 52:2% in

1994. Interestingly, there are also relatively more foreigners in the sample of unemployed workers

in 2000 (26:9%) than in 1994 (22:5%). This pattern concerns all classes of foreign nationalities

except Europeans (other than French), i.e. North Africans, Sub-saharan Africans, and other na-

tionalities. We attribute these e¤ects to dynamic selection biases at the entry into and the exit

out of unemployment. The population at risk is increasingly made of subpopulations that have a

higher entry rate and a lower exit rate since exit rates to a job trended downwards between these

two periods. All in all, the average unemployment duration before �nding a job increases from

235 days to 274 days.

[Insert Tables 2 and 3]

5 The econometric strategy

In theory, all unemployed workers can be a¤ected by the enterprise zone program although individ-

uals are more likely to be a¤ected if they reside in an enterprise zone �because of the requirement

about local employment �or if they live close to an enterprise zone because of spillover e¤ects

which can play in both directions (see our short survey of the literature above). Given that enter-

prise zones are clusters of a signi�cant size within or across municipalities, it would be desirable

to try and detect the e¤ect of the policy� if any� at the level of an enterprise zone. Nevertheless,

our data does not allow us to work at this �ne level of disaggregation and our approach retains

municipalities as our spatial unit of analysis. Municipalities have on average twice the population

19

of the EZ they contain. Any aggregate e¤ect at the municipality level will measure the e¤ect of

local job creation net of within-municipality transfers.

Our raw data consists of individual unemployment spells observed over time. In order to

measure the e¤ect of the EZ program, we start in a �rst stage by estimating semester-speci�c

municipality e¤ects on the propensity to �nd a job while netting out the e¤ects of observed in-

dividual characteristics (gender, age, nationality, diploma, family structure, disability) and the

economic conditions. These municipality e¤ects measure the chances of �nding a job for unem-

ployed workers in each municipality during each semester, all things else being equal. In a second

stage, we then resort to various di¤erence in di¤erences approaches and compare the evolution

of these municipality e¤ects before and after the implementation of the policy between treated

municipalities and various control groups of other municipalities.

In a �rst subsection, we explain how the coe¢ cients of individual variables used as controls are

estimated. In a second subsection, we explain how to recover the semester-speci�c municipality

e¤ects. Finally, in a third subsection, we turn to the estimation of our parameter of interest:

the e¤ect of enterprise zone designation on the exit rate from unemployment to a job at the

municipality level.

5.1 Estimating the e¤ects of individual variables

Consider an individual i who enters unemployment at a given entry date t0i, which is the realization

of a random variable denoted T0i. The unemployment spell of that individual ends when a job is

found or when it is right-censored. Right-censoring groups all other exit types: end of the panel,

dropping out of the labor force or disappearance from the records for an unknown cause.

Denote Ti the latent date at which the individual �nds a job and ti its realization. The corre-

sponding latent duration is Di = Ti � T0i, with realization di. Also denote Tci the latent date of

right-censoring and Dci = Tci � T0i the duration until right-censoring. The observed duration of

20

the unemployment spell is then min(Di; Dci). We assume that the latent duration until �nding a

job and the latent duration ending with right censoring are independent.

For an individual i, we denote ��d��� eXi; j (i) ; t0i

�the hazard rate for exiting to a job at duration d

where eXi is a set of non-time varying individual explanatory variables, and j (i) is the municipality

in which the individual resides. Note that the hazard rate is written as a function of the entry

date t0i for the sake of �exibility.

With these de�nitions in mind, we can now consider a duration model where observations are

clustered by municipality and semester. The time interval between July 1, 1993 and June 30, 2003

is split into S semesters denoted [� q; � q+1). For q = 1; :::; 20. From now on, we will refer to semester

q to designate [� q; � q+1). Denote s =20Xq=1

q:1 f� q � t0i + d < � q+1g the semester during which the

unemployed worker i exits after an unemployment spell of duration d (ie. t0i+d 2 [� s; � s+1)). The

hazard rate function is speci�ed as proportional:

��d��� eXi; j (i) ; t0i

�= �j(i) (d; s) exp (Xi�s) (1)

where �j (d; s) is the baseline hazard rate in municipality j during semester s, and Xi =h eXi; Ai

iwhere Ai are indicators of months and years of entry calculated from t0i. The vector of parameters

�s =h�eX0s ; �

A0s

i0can be decomposed into parameters corresponding to the individual variableseXi (denoted �

eXs ) and parameters corresponding to the indicators of months and years of entry

(denoted �As ). The hazard rate is assumed to depend on both semesters and municipalities to take

into account the possibility that local policies and local economic conditions may vary over time.

We follow Gobillon, Magnac and Selod (2010) who extend the set-up proposed by Ridder and

Tunali (1999) of Strati�ed Partial Likelihood Estimation (SPLE) which itself is a generalization of

Cox Partial Likelihood. To start with, we estimate the e¤ects of individual explanatory variables

allowing for �xed cluster e¤ects (i.e. semester-speci�c municipality e¤ects in our case). Denote

j (d; s) the set of individuals at risk in municipality j during semester s for a duration d, i.e.

the set of all individual unemployment spells which reach at least duration d during semester s.

21

The risk set of an individual i who resides in municipality j(i) and whose unemployment spell

lasts a duration di until an exit to a job occurs during semester si, is given by <i = j(i) (di; si).

An unemployed worker ` is in the risk set <i under three conditions. The unemployed worker `

should be a resident of municipality j (i); the observed duration of the unemployment spell should

be larger than di; the unemployed worker should have been unemployed at least for a duration

di at some date during semester si. Formally, these three conditions can be written: j (`) = j (i),

min (d`; dc`) > di and t0` + di 2 [� si ; � si+1) where t0` is the date of entry and tc` is the date of

right-censoring for individual `.

It is useful to go through a simple example to understand the logic of this construction. Figure

7 explains how unemployment spells are considered in each semester. Two unemployment spells

are represented and cover three semesters. The �rst spell begins during semester 2 and lasts e1

units of time till the end of this semester. The spell reaches the end of semester 3 after a total

duration of e1+ d1, and continues afterwards. The second spell begins during semester 1 and lasts

e2 till the end of this semester. It ends in semester 2 after a complete duration of e2 + d2. The

subsamples of individuals at risk during the �rst three semesters and that we described above are

respectively f2g, f1; 2g and f1g. The set of durations during which there is at least one individual

at risk during semester 1 is the interval [0; e2]. For semester 2, the set is [0; e1][ [e2; e2 + d2] (where

in our example e1 < e2), and for semester 3, the set is the interval [e1; e1 + d1].

Coming back to the thread of our formal discussion, we now derive the Cox partial likelihood

function from the following conditional probability. Individual i �nds a job after an unemployment

spell of duration di during semester si, conditionally on the event that someone in individual i�s

risk set <i �nds a job at duration di during semester si, with the probability given by:

Pi = P (di; si j` 2 <i; (d`; s`) = (di; si)) =exp

�Xi�si

�X`2<i

exp�X`�si

� (2)

Observe that since the risk set is de�ned for each semester and municipality, the baseline hazard

22

disappears from this conditional likelihood function. This baseline hazard can thus depend in

a �exible way on semester-speci�c municipality e¤ects. It is in this sense that this method of

estimation is strati�ed.

The sample partial likelihood function can be written:

L =Yi

Pi =Ys

Ls (�s) (3)

where Ls (�s) = �ijsi=s

Pi is the partial likelihood function of all individuals experiencing an exit

during semester s. Note that a given likelihood function Ls contains terms relative to some indi-

viduals at risk during semester s who do not experience an exit but contribute to the denominator

of (2). In contrast, some individuals at risk during semester s may not be used at all to compute

the likelihood Ls. For instance, denote ds0 the smallest duration at which an individual experi-

ences an exit during semester s in a given municipality. If some individuals are at risk in the

same municipality during semester s only for durations shorter than ds0, then they are not used

to compute Ls. Finally, note that an individual may contribute to several Ls as he may be at risk

at some dates in several semesters.

In practice, it is computationally intractable to maximize the full partial likelihood function L when

both the sample and the number of semesters are large. As our application has N = 8; 831; 456

observations and S = 20 periods, we perform the estimation on subsamples. We maximize each

term Ls with respect to �s on an adequate subsample which contains all the information and

is constructed in the following way. Denote js the subset of individuals at risk in municipality

j during semester s. The subsample of individuals at risk during semester s is then s = [jjs.

The set s contains all the individuals necessary to compute the partial likelihood functions Ls.

Maximizing each Ls separately requires that the coe¢ cients of individual variables in equation (1)

are left free to depend on the semester. This was assumed from the start although had we wished,

we could have imposed the identity of these coe¢ cients across semesters using minimum distance

estimation in a second step. This would have enabled us to obtain coe¢ cients which are constant

23

across semesters. We prefer to use the more �exible estimates so that the policy evaluation is

robust to varying e¤ects of individual characteristics over the business cycle.

5.2 Estimating municipality e¤ects

Given the estimation of coe¢ cients �s we can now recover the baseline hazard functions in each

municipality and for each semester. De�ne the integrated baseline hazard function in a munic-

ipality j for semester s as �js (d) =

dZ0

�j (u; s) du. We construct the Breslow�s estimator of this

function as:

b�js (d) = dZ0

I (Cjs (u) > 0)Pi2js(u)

exp( eXic�eXs )

dN js (u) (4)

wherec�eXs is the SPLE of �

eXs ,

js (u) is the subset of individuals at risk in municipality j during

semester s after duration u (such that we have: js = [ujs (u)), I (�) is the indicator function,

Cjs (u) = card js (u), and dNjs (u) is a dummy that equals one if someone in municipality j

experiences an exit during semester s in an arbitrarily short period of time before date u (and

zero otherwise). Moreover, the variance of b�js (d) for each d can be recovered from the formulas

given in Ridder and Tunali (1999). Its implementation is also detailed in Gobillon, Magnac and

Selod (2010).

Note that we choose not to include the estimates of the �J 0s coe¢ cients (the coe¢ cient of the

dummies for months and years of entry) in the computation of the denominator of (4). We do so

because the estimates of these coe¢ cients pick up a mixture of the calendar time e¤ects at entry

and exit and are not unbiased estimators of the true entry e¤ects. More generally, this stems from

the non-identi�cation of duration and entry e¤ects when no functional form is assumed.

Equation (4) yields an estimate of the integrated baseline hazard function for each municipality and

semester. We could presumably work with various summaries of these functions, for instance the

integrated hazards at 6 months, 12 months, etc., describing the facility with which the unemployed

24

�nd a job in a given municipality. We prefer to summarize the semester-speci�c municipality e¤ects

using a multiplicative speci�cation. The hazard function in a municipality j during semester s takes

the form:

�j (d; s) = �js� (d) (5)

where �js is a semester-speci�c municipality e¤ect and � (d) is a general baseline hazard function.

To estimate the semester-speci�c municipality e¤ects, we break down unemployment duration into

M intervals [dm; dm+1), m = 1; :::;M�1 with d1 = 0 and dM = +1. In our application, the length

of each interval is 90 days except the last one which is unbounded on the right. We denote m the

interval [dm; dm+1) and �m = 1dm+1�dm

dm+1Rdm

� (u) du the average baseline hazard rate over interval

m. The average hazard over a duration interval m in municipality j is given by

yjs;m =1

dm+1 � dm��js (dm+1)��js (dm)

�: (6)

We denote:

�js;m =

dm+1Zdm

I�Cjs (u) > 0

�du

the time in interval m during which some individuals are at risk in municipality j during semester

s. An estimator of the quantity given in (6) when some people are at risk (�js;m > 0) can be

constructed from equation (4). It is given by: yjs;m =1

�js;m[b�js (dm+1) � b�js (dm)]. Using equation

(5), we can set up the estimation of this model as a minimum distance procedure by writing that

ln yjs;m = ln�js + ln �m + "

js;m (7)

where "js;m = ln�yjs;m

�� ln

�yjs;m

�are the residuals describing the sampling variability of estimated

hazard rates. The covariance matrix of these residuals can be recovered from the covariance matrix

of the estimated integrated hazards given by (4).

Nevertheless, we estimate equation (7) by weighted least squares using a simple system of weights

instead of using optimal minimum distance. The poor small sample properties of optimal mini-

mum distance estimation are well known (see for instance Altonji and Segal, 1996, and follow-ups).

25

Other weighting schemes are possible and we tested in Gobillon, Magnac and Selod (2010), al-

though with a much more restrictive set of data, the robustness of our results to these alternative

weights. Our simple weights are given by the number of unemployed workers at risk at the be-

ginning of each duration interval m. Note that this number may not include all individuals of a

given municipality that contributed to the partial likelihood Ls over the interval. Indeed, some

unemployed workers of the municipality may be at risk at semester s inside an interval but not

at the beginning of that interval. Finally, we can derive the covariance matrix of the estimator of

�js from the covariance matrix of semester-speci�c municipality integrated hazards as explained

by Ridder and Tunali (1999).

5.3 Evaluation of the e¤ect of enterprise zones

We can now �nally turn to the evaluation of the e¤ect of enterprise zone designation on the

municipality e¤ects �js estimated above for each municipality j and semester s. These municipality

e¤ects describe the facility with which the unemployed �nd a job in municipality j at semester

s. We distinguish semesters before the creation of enterprise zones that we generically denote s0

(i.e. between the second semester of 1993 and the second semester of 1996) and semesters after

the creation of EZs that we generically denote s1 (i.e. between the �rst semester of 1997 and the

�rst semester of 2003). We adopt the vocabulary of treatment e¤ects when referring to enterprise

zone designation (Rosenbaum and Rubin, 1983). Denote ln�js1 (1) the (logarithm of) municipality

e¤ect in the case in which municipality j is treated. It is the observed or estimated e¤ect in the

case the municipality comprises an enterprise zone in semester s1 and the counterfactual if the

municipality does not host an enterprise zone in semester s1. Similarly, the municipality e¤ect

is denoted ln�js1 (0) when municipality j does not contain an enterprise zone in semester s1. It

is the counterfactual when municipality j does in fact contain an enterprise zone in semester s1.

Now, denote Zj the treatment indicator, a dummy variable that indicates whether municipality

26

j actually comprises an enterprise zone from 1997 onwards. The observed municipality e¤ect in

semester s1 can thus be written as:

ln�js1 = Zj: ln�js1 (1) +

�1� Zj

�ln�js1 (0) :

The average e¤ect of enterprise zone designation on unemployment exits in municipalities which

include enterprise zones after 1997� i.e. the treatment on the treated� is given by:

� = E�ln�js1 (1)� ln�

js1(0)��Zj = 1� :

This cannot be observed since the term E�ln�js1 (0) jZj = 1

�in this expression is a counterfactual.

Assume nevertheless that the change in the municipality e¤ects over time would have been the

same for treated and non-treated municipalities in the absence of the treatment giving:

E�� ln�j (0)

��Zj = 1� = E �� ln�j (0) ��Zj = 0� ; (8)

where we denote� ln�j (z) = ln�js1 (z)�ln�js0 with z 2 f0; 1g. The e¤ect of creating an enterprise

zone can now be rewritten as:

� = E�� ln�j (1)�� ln�j (0)

��Zj = 1�= E

�� ln�j (1)

��Zj = 1�� E �� ln�j (0) ��Zj = 1�= E

�� ln�j (1)

��Zj = 1�� E �� ln�j (0) ��Zj = 0� ; (9)

where the de�nitions of �rst di¤erences were used to obtain the �rst line, and where assumption

(8) was used to obtain the third line.

The �rst right-hand side term in (9) can be estimated from the data on treated municipalities

using the formula: bE �� ln�j (1) ��Zj = 1� = XjjZj=1

!j

�[ln�js1 � [ln�js0

�

where !j is a weight and[ln�js is an estimator of the semester-speci�c municipality e¤ect (which is

estimated in the previous stage). In practice, the weight can be constructed using the share of un-

27

employed workers living in a treated municipality j or using the covariance matrix of municipality

e¤ects obtained in previous stages.

Similarly, the second right-hand side term in (9) can be recovered likewise from the data on

untreated municipalities:

bE �� ln�j (0) ��Zj = 0� = XjjZj=0

!j

�[ln�js1 � [ln�js0

�:

An estimator of the e¤ect of enterprise zone designation is then given by:

b� = bE �� ln�j (1) ��Zj = 1�� bE �� ln�j (0) ��Zj = 0� (10)

In practice, as we will see below, b� is the estimated coe¢ cient of the treatment indicator in aregression weighted by !j of semester-speci�c municipality e¤ects on dummies for municipalities,

dummies for time intervals, and the treatment indicator.

Interestingly, estimates can be obtained using versatile de�nitions of the control group. When

de�ning the control group however, there is a potential con�ict between two objectives. First,

we aim at retaining municipalities that are similar to those in the treatment group along various

dimensions. This suggests that the control group should comprise municipalities that are clos-

est in the space of characteristics, including the location within the Paris region (i.e. neighbor

municipalities). Observe that since political actors had a say in the designation of enterprise

zones, the selection process was not completely based on the ranking according to the aggregate

indicator. This makes it easier to �nd control municipalities with characteristics similar to those

that are treated. Nonetheless, avoiding contamination of the e¤ects through spatial spillovers is

a second objective and this may contradict the �rst objective (Blundell, Costa-Dias, Meghir and

van Reenen, 2006). This is why it makes sense to develop various empirical strategies controlling

for various municipality variables and various ways of constructing the control group.

28

6 Results of the policy evaluation

To start with, we brie�y report the results of the estimation of the strati�ed Cox model which

allows us to estimate spatial e¤ects free of "composition e¤ects" due to individual observed char-

acteristics. We then turn to the evaluation of the creation of enterprise zones on January 1st

1997. We begin with de�ning the treatment parameter and with reporting the estimation of

the propensity score at the municipality level. We then present estimates obtained by matching,

within and �rst di¤erence estimation. We �nally report our preferred speci�cation and provide

various robustness checks.

6.1 Strati�ed partial likelihood estimates

We performed the �rst-stage estimation of the model as given by the partial likelihood (3) for

all semesters between the second semester of 1993 and the �rst semester of 2003. In Table 4,

we report only the results of this estimation for the �rst semester of 1994 and the �rst semester

of 2000. In our policy evaluation, this �rst-stage is used to purge semester-speci�c municipality

rates of exit to a job from individual composition e¤ects and to control for right-censorship in

durations. The e¤ects of socio-demographic characteristics are very similar to those that were

obtained in Gobillon, Magnac and Selod (2010) where we used a single �ow sample instead of

semester speci�c samples. We refer the reader to this paper for a full analysis of these e¤ects

although a brief summary is useful. Unemployed workers who are disabled, who are females or

who have many children, less often experience an exit to a job. Those living in a couple exit

to a job more often and as expected low educated unemployed workers exit to a job less often

than educated ones. Furthermore, Sub-Saharan Africans and North Africans �nd a job far less

often than French people. Noticeably, the situation deteriorated between 1994 and 2000 for low

educated people and Sub-Saharan Africans. This con�rms that rates of exit to a job decreased

29

over this period, speci�cally for the sub-populations who experience a low exit rate.

[Insert Table 4]

6.2 De�nition of the treatment

We estimate the e¤ect of the EZ program using various dates before and after the creation of EZs.

In the setting of Section 5.3, the period s0 now corresponds to all semesters between the second

semester of 1993 and the second semester of 1996 (semester 7 on the Figures) and s1 corresponds

to all semesters between the �rst semester of 1997 (semester 8) and the �rst semester of 2003.

The treatment group is composed of municipalities which comprise an enterprise zone. In

robustness checks we shall also test our results against departures from this construction and will

distinguish municipalities for which enterprise zones represent a large section of their population

(more than 50%) from the other treated municipalities. We will also modify the treatment group

by including neighbors of treated municipalities.

The main substantive issue concerns the control group which in principle could contain all

municipalities which are not in the treatment group. However, this implicitly assumes that all

non-treated municipalities resemble treated municipalities, which is far from being the case. Some

municipalities are too far from the treated municipalities both geographically or in the space of

other characteristics. Most prominently, the population size of a municipality has a very di¤erent

support in the primary treatment and control groups. While the control group comprises many

small and very small municipalities (less than 1,000 inhabitants), the smaller population size of

a treated municipality is 17,500. We thus chose from the start to restrict the control group to

municipalities whose population size is between 8,000 and 100,000.10 Note that it changes the

10The reason for excluding the municipalities over 100,000 inhabitants is that this group includes Paris inner

districts and one close neighbor, Boulogne-Billancourt, which are at no risk of being selected because of their

a­ uence. We chose the lower bound of 8,000 because we wanted to include neighbors of treated municipalities.

We do not know the identity of unsuccessful applicants to the program.

30

de�nition of the treatment parameter which now refers to municipalities with this population size.

Further restrictions on the control group will further modify the de�nition of the "e¤ect of

a treatment" and will be brought in after the construction of the propensity score that we now

detail.

6.3 Describing the treated municipalities: the propensity score

We now analyze the municipality characteristics that determine the creation of an enterprise zone

and that will allow us to construct the propensity score as proposed by Rosenbaum and Rubin

(1983) so as to control for selection on observables. We estimate a discrete model, here Probit, to

explain the status of being designated, z = 1 against z = 0 where we use some municipality control

variables X among which are measures of physical job accessibility, the municipal composition of

the population in terms of nationality or education, the rate of unemployment, the proportion of

young adults, and the �scal potential. We also include in the speci�cation the smallest distance

to another municipality comprising an enterprise zone. This is to account for the possible will

of authorities to spread enterprise zones more or less evenly throughout the region.11 Results

of weighted Probit estimations where the weights are the (square root of the) population size of

unemployed workers in the municipality are reported in Table 5. The results of our benchmark and

preferred speci�cation appear in the �rst column although some less parsimonious speci�cations

were also estimated (see the notes below this Table).

[Insert Table 5]

In conformity with the selection criteria, the larger the �scal income in the municipality or the

smaller the proportion of persons without a high school diploma in the municipality, the less likely

the municipality comprises an enterprise zone although the latter e¤ect is hardly signi�cant. The

11We checked endogeneity issues by experimenting with the second-lowest distance as an instrument. It hardly

a¤ected results.

31

higher the rate of individuals below 25 or the larger the size of the population, the larger the

probability that the municipality contains an enterprise zone. In terms of distance, the larger

the distance to a designated municipality or the larger the density of jobs attainable in less

than 60 minutes by private vehicle, the less likely it is that the municipality will be endowed

with an enterprise zone. This is consistent with the targeting of places with relatively lower

job accessibility. Also, since designated areas are clustered around Paris, they all have another

designated area as a close neighbor, explaining the negative sign on the distance to the nearest

EZ (although not signi�cant). In line with Hanson (2009), we also experimented with political

variables which are the frequency of votes for political parties. Even if municipalities whose

townhalls were administered by politicians belonging to the governing party at the time of EZ

designation are more likely to be picked up, the e¤ect is not signi�cant and we chose not to include

these variables in the �nal speci�cation.

In the two other columns of Table 5, we experimented two alternatives. We �rst included a vari-

able equal to the average of municipality e¤ects a¤ecting exit rates to a job in the semesters before

the implementation of the policy (as estimated in the �rst step by Strati�ed Partial Likelihood).

We chose the average of these e¤ects because the average was the most signi�cant predictor of the

propensity score. The e¤ect is positive although it is at the limit of signi�cance. This means that

the municipalities including a designated area seem to be more advantaged in term of easiness

for exiting unemployment than the other municipalities sharing the same local characteristics.

This is a standard result in the evaluation literature where governments often intervene to "pick

winners" (Boarnet and Bogart, 1996). We also ran the Probit regression using no weights and

though standard errors are larger, the e¤ect of variables remains qualitatively the same. We will

test later for the robustness of our complete results to these changes in speci�cation.

Using the results in column 1, we predict the propensity score for each municipality. It inter-

estingly reveals that the supports of the predicted propensity scores in the treated and control

32

groups di¤er quite markedly as shown in Table 6.

[Insert Table 6]

The smallest predicted probability in the treatment group is equal to 0.1%. We therefore further

restrict the control group to municipalities whose predicted propensity scores are larger than the

value 0.05% (see Table 6). It is roughly two times smaller than the unrestricted control group

and includes 135 municipalities (instead of 258), which is equal to about ten times the number

of treated municipalities (13). We will later test the robustness of our results to more or less

restrictive selections.

6.4 Matching, within and �rst-di¤erences

We chose to estimate linear models of treatment e¤ects given that the number of treated mu-

nicipalities is quite small (13) with respect to the number of controls (135). As explained in the

econometric section and following Imbens and Wooldridge (2009), we started from the following

baseline regression :

[ln�js = �Zjs +Xj� + �s + �j + ujs (11)

where s is the semester, j a municipality and ujs is an error term (including the sampling error

on the left-hand side variable due to �rst-stage estimation). Parameters �s denote time dummies

(for semesters) and �j is a municipality e¤ect. Variable Zjs is the dummy for treatment status, Xj

are control variables which do not vary across time in our database.

Using an orthogonality argument of Rosenbaum and Rubin (1983), we have:

E(ujs j Zjs ; Xj) = 0 =) E(ujs j Zjs ; Xj; p(Xj)) = E(ujs j Zjs ; p(Xj)) = 0; (12)

Hence, we can replace from now on the explanatory variables by the propensity score p(Xj)

although we experimented with general speci�cations.

33

The regression set-up (11) delivers the parameter of interest, �, which is equal to the average

treatment on the treated. A natural weight to use is the number of unemployed workers in the

municipality at the beginning of each semester. We shall also check the robustness of the results

using alternative weights such as the inverse of the estimated standard error of the estimate[ln�js:

An important aspect of the speci�cation is the inclusion of a full set of time-constant munic-

ipality e¤ects, �j, in regression (11). Nevertheless, we can start from a more parsimonious form

where we only include the indicator variable that a municipality comprises a designated enterprise

zone, so that �j = �D:1fj is designatedg. This restriction grants more identi�cation power when

estimating � in equation (11) at the cost of reinforcing the restrictiveness of the orthogonality

condition described by equation (12). We shall see that this restrictive condition is rejected by the

data and that a full set of municipality e¤ects is needed.

We �rst run a basic regression without any controls whose results are reported in Table 7,

column (1). The e¤ect of the dummy for including a designated area, �D, is negative and signi�cant

which con�rms that in a treated municipality, the unemployed are receiving and accepting a job

with a lower probability. Our parameter of interest, the treatment parameter, is estimated to be

negative but insigni�cantly di¤erent from zero. It does not seem to be an issue stemming from

large standard errors since the order of magnitude of the standard error is approximately the same

as for the previous designation e¤ect.

[Insert Table 7]

To go further, we introduce the propensity score as it was estimated in Table 5 column (1)

and Table 7 column (2) reports the results. Firstly, the coe¢ cient of the predicted propensity

score is strongly signi�cant and negative. Potentially treated municipalities have a signi�cantly

lower exit rate to employment. Secondly, note that the sign of the coe¢ cient of a designated

municipality e¤ect, �D, changes in comparison with column (1): it is now positive and very

signi�cant. Enterprise zones were created in municipalities where the chances of �nding a job

34

are signi�cantly larger when holding constant the characteristics that explain the treatment i.e.

through the propensity score. It con�rms the e¤ect of �picking winners�that we identi�ed from

the results on the propensity score in Table 5. In contrast, controlling for the propensity score

does not a¤ect the estimate of �. It remains insigni�cantly di¤erent from zero at the 10% level

and a large standard error is not responsible for the lack of impact. We also experimented with a

more �exible speci�cation for the propensity score using splines without any substantial e¤ect as

reported in column (3) of Table 7. Finally, we obtain the same results when we use the subsample

of larger predicted propensity scores only, municipalities being selected if they are above the 10th

percentile of the propensity score in the treatment group.

Our next step is to present results when we include unrestricted municipality e¤ects, �j. There

are two common ways to proceed and they should yield the same results if the econometric model

is correctly speci�ed. They consist in the use of within estimation or �rst-di¤erences to eliminate

the municipality e¤ects (see for instance Blundell and Costa-Dias, 2009). These estimates are

reported in Table 8 where the �rst column repeats the matching results from Table 7, the second

column reports results of the within estimation using robust-to-heteroskedasticity standard errors

and the last column reports results in �rst di¤erences using robust-to-heteroskedasticity standard

errors.12

Di¤erences across estimation methods are striking as can be seen on Table 7. While the

estimated coe¢ cient for the treatment indicator in within estimation remains negative at about

the same level as the matching estimate, this estimate is signi�cant at the 10% level. In sheer

contrast, the estimate of the treatment parameter using �rst di¤erences is positive (0.049) and

signi�cant at the 1% level. However, these estimators should converge to the same value. Our

econometric model in which the treatment parameter is constant over time is thus rejected by the

12None of the standard errors are corrected for autocorrelation because this will be done in the next section in

a more general context. These corrections are likely to be more severe in �rst di¤erence estimation.

35

data.

[Insert Table 8]

Given our long period of observation, we can plausibly argue that the assumptions underlying

di¤erence-in-di¤erences are not valid and that medium-term trends are di¤erent in treated and

control municipalities. This is why we perform the same analysis by matching, within and �rst-

di¤erences although we now allow the treatment parameters to vary period by period after the

treatment. Table 9 reports such results and shows that indeed the e¤ect of the treatment seems to

have a negative trend using all methods of estimation. The short-run treatment e¤ects as estimated

by matching and within estimation are now positive although insigni�cant in the semester after

treatment. They are either positive or negative but still insigni�cant after the implementation of

the treatment. After semester 14, that is after the �rst semester of 2000, the e¤ects estimated by

matching and within estimation are all negative and some of them are signi�cant.

[Insert Table 9]

In contrast, most e¤ects using �rst di¤erences are positive and larger in the short run than in

the medium term (at least until semester 16) and con�rm results obtained in Table 8. Estimated

treatment e¤ects are consistently in the range 0.025-0.059 for periods before semester 14 although

only two of these estimates are signi�cant.13 In contrast, estimates become smaller or negative

after semester 14 but grow again after semester 17. There are therefore two reasons to think

that our global evaluation relies too much on the medium run evaluation after semester 14. From

Figures 1 and 2, we know that unemployment started trending upward at around semester 14 and

that, more importantly, the exit rate from unemployment attributable to unknown exits changed

signi�cantly from period 13 onwards. This is why we now restrict our analysis to periods 1 to 12,

between the second semester of 1993 and the �rst semester of 1999, a period in which the exit

rate to a job decreases, the unemployment rate is stable or decreases moderately and the rate of

13Correcting for autocorrelation a¤ects standard errors (see below).

36

exits for unknown reasons is stable. We do not take a stand on whether the treatment e¤ects

would disappear after three years or whether the implicit underlying assumption of the di¤erence-

in-di¤erences method about common period e¤ects between treated and control municipalities

would be wrong.

6.5 Our preferred speci�cation

Table 10 reports results of �rst di¤erence estimation correcting for within-municipality autocor-

relation by FGLS using an unrestricted covariance matrix between semester-speci�c municipality

shocks over time. We present results that we obtain when varying the range of semesters used in

the estimations.14

[Insert Table 10]

The �rst column reports the results of our preferred speci�cation since this speci�cation is robust

to various changes in the underlying construction and seems to be a conservative estimate. The

estimated treatment parameter is equal to .031 and is signi�cant at the 5% level. This e¤ect is

quite small since it implies that the rate of exit to a job increased by a meagre 3% when the policy

was implemented. Given that there are roughly 300 exits each semester in an average municipality

in the considered range of population size, the policy amounts to generating about 10 new exits

per semester only.

We included as an explanatory variable the propensity score to control for any residual un-

observed municipality heterogeneity.15 It amounts to considering that municipalities could have

heterogeneous trends in their exit rates, something which might be more likely in a period in

which exit rates to a job have a strong downward trend (between the second semester of 1993 and

the �rst semester of 2000, see Figure 2). These trends are supposed to be random conditional

14We do not report the estimated semester e¤ects. They reproduce closely the raw trends as graphed in Figure

2.15We did not correct for the generated regressor issue that such an inclusion implies.

37

on observables (Heckman and Hotz, 1989) so that a much less restrictive orthogonality condition

than equation (12) holds, namely:

E(ujs � ujs�1 j Zjs ; p(Xj)) = 0:

This assumption was exploited by Heckman, Ichimura and Todd (1997) and this approach belongs

to matching di¤erence-in-di¤erences methods as described by Blundell and Costa-Dias (2009). We

use it in a linear regression setting because our samples are small.

In the second column we further restrict the period of evaluation, keeping only two semesters

before the reform and two semesters after the reform. The estimate remains signi�cant and stands

at .042. If we further restrict to the period at which the reform was implemented, the estimate is

equal to .035 although it becomes insigni�cant. The treatment variable is very much correlated

with the propensity score and when we omit the latter, the estimate increases to .058 and is

signi�cant at the 1% level, which corresponds to a signi�cant doubling of the e¤ect. It might

however re�ect that some �rms delayed hiring during the last semester of 1996 in order to bene�t

from the policy in the following semester although we do not �nd evidence of such opportunism

below.

Interestingly, we can distinguish between treated municipalities according to the proportion

of the municipality population which resides within the enterprise zone. Speci�cally, we included

in our preferred speci�cation an indicator that the proportion of the population living in the

enterprise zone in the treated municipality is below 50%. The result is striking since the treatment

parameter estimate is now equal to .057 instead of .031 and is signi�cant at a 1% level while the

treatment e¤ect in municipalities where a small proportion of the population lives in an enterprise

zone is also positive (.016=.057-.041) but becomes insigni�cant. The dilution of the e¤ect will

be con�rmed below when changing the treatment de�nition. It points out that the e¤ect of the

policy is very localized.

38

6.6 Spillover e¤ects

We now investigate the possibility of spatial spillovers on neighboring municipalities. In theory,

spatial spillovers for neighboring areas can either be positive (if workers in neighboring areas

bene�t from the expansion of the activity in the EZ) or negative (if jobs are relocated away from

neighboring areas, or if some substitution of non-EZ jobs with EZ jobs occur). A �positive�

externality on non-EZ areas may occur if the policy adversely leads to the stigmatization of EZ

residents, with employers discriminating against EZ residents and becoming more likely to hire

workers residing outside the EZ.

To assess these e¤ects, we began with changing the composition of the control group. We

selected municipalities in the control group depending on their distance to a treated municipal-

ity. We experimented with three distance thresholds at 5, 10 and 15 kilometers where these

distances are taken between municipality centres. We �rst restricted the previous control group

to municipalities whose center is farther than 5 kilometers of the center of a treated municipality

(respectively 10 and 15 kilometers). Second, we restricted the control group to municipalities

whose center is within 5 kilometers of the center of a treated municipality (respectively 10 and

15). Table 11 reports these results.

[Insert Table 11]

The evidence of spillover e¤ects to neighboring municipalities is weak. In all but one of these

experiments, the estimates of the treatment parameter remains around .03 although with some

degree of variation in the signi�cance of the estimates. The only case in which the estimate becomes

hardly distinguishable from zero is when the control group is restricted to municipalities outside

the 15 km range of a treated municipality. In our opinion, the assumption that these municipalities

are a¤ected by the same period e¤ects as the treated municipalities becomes unsustainable since

these municipalities correspond to distant zones where the labor market conditions are likely to

be di¤erent.

39

We also attempted to change the de�nition of the treatment, and the composition of the

treatment and control groups. Instead of retaining the municipalities comprising an enterprise

zone only, we also retained their neighbors at a distance of less than 2 kilometers (respectively at

a distance of less than 3 kilometers). The number of potentially treated municipalities increases

from 13 to 24 treated municipalities (respectively 51). Table 12 reports these results. It is striking

that in both cases the estimated treatment parameter is no longer signi�cantly di¤erent from zero.

It con�rms that the creation of an enterprise zone has a very localized e¤ect on the unemployment

exit rate to a job as was already seen in Table 10. It has no signi�cant spillover e¤ects on

neighboring municipalities.

[Insert Table 12]

6.7 Other robustness checks

We also performed other robustness checks of these results. First, we modi�ed the whole procedure

so as to include the past average of municipality e¤ects in the propensity score. Second, we varied

the municipality-and-semester speci�c weights that we used in the estimation. Instead of using

the (square root of the) number of unemployed workers in the municipality at the beginning of

the semester, we used the (inverse) standard errors of the estimates of the left-hand side variable

as provided by the �rst-stage estimates or no weights at all. Table 13 presents these results which

are hardly di¤erent from those obtained for the main speci�cation and if anything, estimates of

the treatment parameter are becoming larger.

[Insert Table 13]

Moreover, the construction of the semester-speci�c municipality e¤ects purges exit rates to jobs

from individual characteristics although it does a poorer job at controlling for entry e¤ects be-

cause of identi�cation issues. We included year and month dummies in the �rst stage estimation

notwithstanding that identi�cation of these parameters from baseline duration hazard could be

40

fragile. This is why we re-estimated our preferred speci�cation controlling for semester and mu-

nicipality speci�c entry rates. Results are presented in the �rst two columns of Table 14. In the

�rst column (respectively the second column), we control for the log-entry rate in the current

period (resp. the lagged log-entry rate). Although this variable has a signi�cant and positive

(resp. negative and not signi�cant) e¤ect, the estimate of the treatment e¤ect is hardly a¤ected

and remains equal to approximately .03.

[Insert Table 14]

Lastly, to measure placebo e¤ects, as suggested by Manning and Pischke (2006) we also included in

the speci�cation an indicator for the lagged treatment e¤ect. If the policy is anticipated, however,

a negative e¤ect could be observed if employers delay hiring decisions. The lagged treatment

e¤ect is found not to be signi�cantly di¤erent from zero and not to a¤ect the estimated treatment

parameter.

6.8 Policy evaluation of related outcomes

We also performed the same evaluation using as dependent variable the raw entry rates into

unemployment as in Papke (1994) and the three raw exit rates from unemployment that we can

construct from our data. Recall indeed that an exit can have three di¤erent destinations: a job,

non-employment or an unknown reason.

We check whether the results with raw rates are comparable with those obtained by applying

our more sophisticated method that purges exit rates to a job from individual characteristics and

takes into account the usual censorships that a¤ect unemployment data. This is a useful check

to perform since policy analysts often resort to raw rates to perform policy evaluations. Table 15

reports these results.

[Insert Table 15]

In column 1, the parameter which measures the e¤ect of the treatment on the log-entry rates in

41

unemployment is not signi�cantly di¤erent from zero. Column 2 reports the e¤ect of the treatment

on the log-exit rates out of unemployment to a job. It is signi�cantly positive and equal to .040.

It is thus slightly larger than the estimate that we obtain using our two step procedure to purge

exit rates from composition e¤ects (in terms of observed individual characteristics) although the

di¤erence is insigni�cant. The di¤erence may come either from composition e¤ects or from right-

censored unemployment spells. In the somewhat restricted sense that the conclusion applies to

this speci�c dataset, it suggests that the estimates using raw data could in fact be reasonable

approximations.

Evidence gathered in Tables 14 and 15 runs against an argument advanced by Elverly (2009)

about indirect e¤ects of employment zones. The local labour market in treated municipalities

would become more attractive after the creation of an enterprise zone and non-employed persons

would be encouraged to search for a job. This would increase the entry rate into unemployment and

the competition for jobs among the unemployed. We neither �nd that the treatment parameter is

a¤ected by entry rates (Table 14) nor that entry rates change because of the program (Table 15).

The estimates of the treatment parameter for exits to non-employment and exits for unknown

reasons are not signi�cantly di¤erent from zero although the estimate for exits to non-employment

is quite large at the same level .039. Contrary to the stylized facts in the descriptive section above,

the censorship due to exits for unknown reasons does not seem to be a¤ected by the policy. Our

estimated parameter is thus robust to the consideration that some exits for unknown reasons

might be exits to a job triggered by the EZ policy.

7 Conclusion and policy discussion

In this paper, we have evaluated the e¤ects of enterprise zones in the Paris region on exit rates

from unemployment to employment at the municipality level.

Our main results are threefold. Firstly, in line with several studies on enterprise zones, we

42

showed that zone designation tended to favor municipalities with favorable unobserved charac-

teristics. This is not surprising given that policy makers usually tend to select places that are

more likely to carry success or choose places that gather prior favorable conditions for economic

development. Secondly, we found that the French EZ program had a small positive impact, which

is consistent with previous work on the number of local establishments in enterprise zones (Rath-

elot and Sillard, 2009). The policy had a short-run impact on the ease with which the local

unemployed workers move out of unemployment. This result is robust to a variety of speci�cations

and robustness checks and is broadly in line with the previous works in the US that found that

enterprise zones had a small impact on employment (Papke, 1994, Lynch and Zax, 2008, Neumark

and Kolko, 2010) and contrasts with those which found that it had no impact on employment

(Boarnet and Bogart, 1996, Bondonio and Engberg, 2000). Lastly, we �nd that the e¤ect is very

localized and seems to be the direct consequence that tax rebates are given in exchange of the

requirement that some locals should be hired.

The estimated e¤ect of the policy on unemployment is small and represents a 3% increase in

the rate of exit from unemployment to jobs. This is in contrast with the �gure of a 30% increase in

the number of jobs in the treated EZ reported by Gilli (2006) for the same period. This suggests

that the substitution of jobs from non-EZ to EZ areas may indeed have been quite large but may

have had an overall e¤ect on employment that was almost neutral. It is also likely that the policy

may have tended to stimulate exits from non-employment �which we are not able to measure with

our data. Finally, external e¤ects on non-economic outcomes may also have been triggered by the

EZ policy. We leave these issues for future research.

43

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perimental Estimators", Journal of Econometrics, 125, 305-353.

[40] Thélot H. (2004) "Les embauches en zone franche urbaine en 2002", Premières Informations,

Premières Synthèses, N�35.1.

47

Table 1: Descriptive statistics of the exhaustive sample, by semester

All municipalities Municipalities whose population isbetween 8,000 and 100,000 in 1990

Year Semester Nb. at risk Exit to job Nb. at risk Exit to job

1993 2 1,139,991 127,748 795,570 89,404

1994 1 1,144,764 144,094 799,234 100,743

1994 2 1,201,196 140,438 837,624 98,051

1995 1 1,153,306 140,389 802,327 98,364

1995 2 1,168,106 135,768 813,158 94,885

1996 1 1,131,391 139,655 790,664 97,521

1996 2 1,171,410 123,759 818,334 86,350

1997 1 1,111,631 124,091 778,704 86,490

1997 2 1,140,782 111,852 800,008 77,843

1998 1 1,090,633 114,619 768,067 79,910

1998 2 1,122,653 102,765 791,357 71,850

1999 1 1,085,102 105,976 765,103 73,381

1999 2 1,101,209 100,188 776,471 70,061

2000 1 1,026,096 103,761 723,854 72,330

2000 2 970,200 95,736 687,451 67,035

2001 1 905,301 86,233 640,140 60,183

2001 2 936,464 76,388 661,347 53,769

2002 1 960,918 77,619 678,313 54,336

2002 2 1,061,983 79,513 747,329 55,657

2003 1 1,074,594 77,036 755,211 53,521Nb. at risk: number of unemployed workers whose unemployment spell began within the four-year period before

the beginning of the semester and who are at risk at least one day during the semester.

Exit to job: number of unemployed workers exiting to a job during the period.

48

Table 2: Descriptive statistics of the sample at risk in the first semester of 1994

Variable N.Obs. Mean Std

Exit types and unemployment spellsExit to job in the period 1,144,762 0.126 0.476Exit to non-employment in the period 1,144,762 0.058 0.373Unknown exit in the period 1,144,762 0.196 0.551Duration if exit to job in the period 144,092 234.810 560.812Duration if exit to non-employment in the period 66,196 275.532 733.689Duration if unknown exit in the period 224,829 207.517 584.673

Characteristics of unemployed workersAge 1,144,762 33.010 9.394Male 1,144,762 0.522 0.500Female 1,144,762 0.478 0.500Single 1,144,762 0.563 0.496Couple 1,144,762 0.437 0.496No child 1,144,762 0.580 0.4941 child 1,144,762 0.173 0.3792 children 1,144,762 0.138 0.3453 children 1,144,762 0.061 0.2404 children 1,144,762 0.024 0.1535 children and more 1,144,762 0.023 0.149French 1,144,762 0.775 0.417European (other) 1,144,762 0.065 0.247North African 1,144,762 0.080 0.272Subsaharan African 1,144,762 0.046 0.210Other Nationality 1,144,762 0.033 0.178College diploma 1,144,762 0.217 0.412High School (final year and diploma) 1,144,762 0.148 0.355High school (excluding final year) and technical diploma 1,144,762 0.318 0.466Secondary school and no diploma 1,144,762 0.317 0.465Disabled 1,144,762 0.028 0.164

49

Table 3: Descriptive statistics of the sample at risk in the first semester of 2000

Variable N.Obs. Mean Std

Exit types and unemployment spellsExit to job in the period 1,026,093 0.101 0.424Exit to non-employment in the period 1,026,093 0.058 0.361Unknown exit in the period 1,026,093 0.253 0.563Duration if exit to job in the period 103,758 274.313 548.811Duration if exit to non-employment in the period 59,776 327.977 689.502Duration if unknown exit in the period 259,276 263.671 545.119

Characteristics of unemployed workersAge 1,026,093 34.620 9.567Male 1,026,093 0.491 0.500Female 1,026,093 0.509 0.500Single 1,026,093 0.562 0.496Couple 1,026,093 0.438 0.496No child 1,026,093 0.613 0.4871 child 1,026,093 0.155 0.3622 children 1,026,093 0.124 0.3293 children 1,026,093 0.063 0.2434 children 1,026,093 0.025 0.1565 children and more 1,026,093 0.020 0.141French 1,026,093 0.731 0.444European (other) 1,026,093 0.064 0.245North African 1,026,093 0.093 0.290Subsaharan African 1,026,093 0.068 0.252Other Nationality 1,026,093 0.044 0.206College diploma 1,026,093 0.244 0.430High School (final year and diploma) 1,026,093 0.173 0.379High school (excluding final year) and technical diploma 1,026,093 0.290 0.454Secondary school and no diploma 1,026,093 0.293 0.455Disabled 1,026,093 0.045 0.208

50

Table 4: Results of the first-stage estimation, semester 1 in years 1994 and 2000

1st semester 1994 1st semester 2000Age/100 -4.153*** -1.670***

(0.251) (0.282)(Age/100) squared 3.201*** -0.282

(0.353) (0.390)Male <ref> <ref>

Female -0.183*** -0.201***(0.005) (0.006)

Single <ref> <ref>

Couple 0.128*** 0.107***(0.007) (0.008)

No child <ref> <ref>

1 child -0.111*** -0.085***(0.009) (0.010)

2 children -0.096*** -0.003(0.010) (0.011)

3 children -0.171*** -0.075***(0.014) (0.016)

4 children -0.175*** -0.100***(0.023) (0.026)

5 children and more -0.238*** -0.135***(0.027) (0.033)

French <ref> <ref>

European -0.014 -0.058***(0.012) (0.014)

North African -0.402*** -0.383***(0.013) (0.014)

Subsaharan African -0.723*** -0.752***(0.019) (0.019)

Other Nationality -0.536*** -0.719***(0.021) (0.023)

College diploma <ref> <ref>

High School (final year and diploma) -0.234*** -0.292***(0.008) (0.009)

High school (excluding final year) and technical diploma -0.320*** -0.338***(0.007) (0.008)

Secondary school and no diploma -0.583*** -0.629***(0.009) (0.010)

Not disabled <ref> <ref>

Disabled -0.371*** -0.381***(0.021) (0.019)

Number of individuals at risk 1144762 1026093Number of exits within the interval 144092 103758Mean log-likelihood -6.281 -6.028

Note: ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.

51

Table 5: Propensity score: the effect of municipality characteristicson the designation of an enterprise zone

Weights Weights, inclusion of No weightspast municipality effect

Job density, 60’ by private vehicle -3.999* -3.357 -4.171*(2.109) (2.260) (2.298)

Proportion of no diploma 37.779* 33.447 24.029(22.249) (23.998) (22.865)

Proportion of technical diplomas 20.998 5.860 0.974(28.215) (31.527) (28.900)

Proportion of college diplomas 38.978 27.180 17.299(29.889) (32.809) (31.336)

Distance to the nearest EZ -0.027 -0.033 -0.035(0.024) (0.025) (0.024)

Proportion of individuals below 25 in 1990 17.125*** 14.890*** 11.834**(5.156) (5.320) (5.256)

Population in 1990 0.021** 0.022** 0.019*(0.009) (0.009) (0.011)

Average net income in 96 -4.975*** -5.140*** -2.033(1.563) (1.636) (1.593)

Past municipality effect in exit to job 4.014*(2.323)

Constant -32.115 -1.447 -16.526(21.818) (29.243) (22.537)

Nb. observations 271 271 271Pseudo-R2 .542 .561 .477

Note: ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.

The sample is restricted to municipalities with a population between 8,000 and 100,000 in 1990. The first and

second columns are weighted by the square root of the number of unemployed workers at risk at the beginning

of period 8, and the third column is not weighted. Past municipality effect refers to the average of municipality

effects in previous semesters, as estimated in the 1st stage (SPLE).

We also used alternative specifications including in the set of explanatory variables, for instance: the job density

within a 60’ radius by public transport, the unemployment rate in 1990, the proportions of Europeans (French

excluded), North Africans, Subsaharan Africans and other nationalities. The estimated coefficients were not

significant and a Chi-square test did not reject the absence of joint significance. Consequently, we dropped these

variables from the specification.

Table 6: Descriptive statistics on the propensity score in treated and control groups

Group Nb. obs. Mean Std. Dev. Min Max

Non-treated 258 .034 .093 0 .643

Non-treated, propensity score > .0005 135 .065 .121 0 .643

Treated 13 .497 .352 .001 .995

Note: The observation unit is a municipality between 8,000 and 100,000 inhabitants. The propensity score was

computed from the results of Table 5, column (1).

52

Table 7: The effect of designation and treatment on semester-specific municipality effects (OLS)

No control Propensity score Propensity score Propensity scoresupport : z > zmin support : z > zmin support : z > zmin support : z > z10

Score in splinesMunicipality -.035** .074*** .043** .070***designated for an EZ (.017) (.019) (.017) (.020)EZ treatment effect -.024 -.023 -.021 -.030

(.022) (.021) (.019) (.023)Propensity score -.229*** -.154***

(.018) (.020)P. score, spline 1 -3.42***

(.41)P. score, spline 2 -.394***

(.131)P. score, spline 3 .863***

(.132)P. score, spline 4 -1.008***

(.114)P. score, spline 5 -.099

(.069)Nb observations 2960 2960 2960 2960R2 .510 .534 .571 .512

Note: ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.

Weight: number of unemployed workers at risk. Year dummies are included and are not reported here. The

standard errors are computed using the sandwich formula and the generated regressor issue due to the estimated

propensity score is not corrected. zmin: minimum of the score for the treated municipalities divided by two.

z10: first decile of the score for treated municipalities. Value of the bounds for splines determined so that treated

municipalities are allocated equally in categories.

53

Table 8: The effect of designation and treatment on semester-specific municipality effects:Matching, within and first-difference

Matching Within estimator First-differenceMunicipality .074***designated for an EZ (.019)EZ treatment effect -.023 -.024* .049***

(.021) (.012) (.019)Propensity score -.229***

(.018)Weight nut nut nut−1 + nut

Nb observations 2960 2960 2812

Note: ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.

Standard errors are robust to heteroskedasticity. nut: number of unemployed workers at risk at period t. Year

dummies are included and are not reported here.

54

Table 9: The effect of designation and treatment on semester-specific municipality effectstreatment effect varying with time

Matching Within estimator First-differenceMunicipality 0.074***designated for an EZ (0.019)Propensity score -0.229*** -0.009

(0.018) (0.006)Treatment effect, 0.010 0.011 0.043**semester 8 (0.046) (0.022) (0.022)Treatment effect, -0.006 -0.005 0.039semester 9 (0.043) (0.022) (0.026)Treatment effect, 0.025 0.022 0.059*semester 10 (0.052) (0.028) (0.031)Treatment effect, -0.016 -0.020 0.027semester 11 (0.043) (0.019) (0.036)Treatment effect, -0.011 -0.015 0.030semester 12 (0.054) (0.026) (0.040)Treatment effect, -0.026 -0.029 0.025semester 13 (0.055) (0.025) (0.044)Treatment effect, 0.011 0.007 0.054semester 14 (0.055) (0.021) (0.048)Treatment effect, -0.062 -0.063** -0.015semester 15 (0.060) (0.028) (0.052)Treatment effect, -0.023 -0.027 0.024semester 16 (0.053) (0.031) (0.056)Treatment effect, -0.060 -0.062** 0.005semester 17 (0.052) (0.028) (0.060)Treatment effect, -0.032 -0.033 0.053semester 18 (0.054) (0.026) (0.064)Treatment effect, -0.045 -0.044 0.038semester 19 (0.049) (0.033) (0.068)Treatment effect, -0.069 -0.067* 0.019semester 20 (0.057) (0.035) (0.071)Constant -6.861*** -0.016** -0.125***

(0.019) (0.007) (0.009)Weight nut nut nut−1 + nut

Nb observations 2960 2960 2812R2 .535

Note: ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.

nut: number of unemployed workers at risk at period t. Year dummies are included and are not reported here.

Standard errors are robust to heteroskedasticity.

55

Table 10: The effect of designation and treatment on semester-specific municipality effectsrobustness to changes of semesters,

specific effect for EZ with a small proportion of the population in the municipality

Periods: Periods: Period: Period: Specific effect forless than 13 5 to 9 8 8 small-proportion EZ

EZ treatment effect .031** .042** .035 .058*** .057***(.014) (.019) (.025) (.019) (.016)

EZ treatment effect -.041**X small-proportion EZ (.018)Propensity score -.008* -.021* .049 -.007*

(.004) (.012) (.039) (.004)Nb observations 1628 592 148 148 1628

Note: ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.

Year dummies are included and are not reported here. Small-proportion EZ are the EZ whose population accounts

for less than 50% of the population of the municipalities where the EZ is located. Estimation method: FGLS

with a constant within-municipality unrestricted covariance matrix.

56

Tab

le11

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Con

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ontr

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oup:

Con

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oup:

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ontr

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nom

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nom

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ies

wit

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5km

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Zw

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n10

kmof

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wit

hin

15km

ofE

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wit

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trea

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.033

**.0

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004)

Nb

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ions

1133

737

462

638

1034

1309

Note

:***:

signifi

cant

at

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level

;**:

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;*:

signifi

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.

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ix.

57

Table 12: The effect of designation and treatment on semester-specific municipality effects,robustness to changes in the specification of the treatment group

Treatment group: Treatment group: Treatment group:municipalities with municipalities less municipalities less

an EZ than 2km of an EZ than 3km of an EZEZ treatment effect .031** .010 .009

(.014) (.012) (.010)Propensity score -.008* -.003 -.001

(.004) (004) (.004)Nb observations 1628 1947 1881

Note: ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.

Year dummies are included and are not reported here. We only keep semesters between 1 and 12. Estimation

method: FGLS with a constant within-municipality unrestricted covariance matrix. ”Municipalities with an EZ”

corresponds to our baseline treatment group and includes 13 municipalities. There are 24 municipalities within

2km of an EZ and 51 municipalities within 3km of an EZ.

58

Table 13: The effect of designation and treatment on semester-specific municipality effects,robustness to changes in the specification of the propensity score and weighting scheme

Propensity score: Weighting: Weighting:inclusion of average inverse of the no weightsof past municipality 1st stage

effects standard errorsEZ treatment effect .032** .029** .042***

(.014) (.014) (.016)Propensity score -.008** -.048 -.013***

(.004) (.030) (.005)Nb observations 1518 1617 1276

Note: ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.

Year dummies are included and are not reported here. We only keep semesters between 1 and 12. Estimation

method: FGLS with a constant within-municipality unrestricted covariance matrix. The results of the propensity

score equation when including the average of past municipality effects is given in Table 1, column 2.

59

Table 14: The effect of treatment on semester-specific municipality effects,robustness to the inclusion of the present and past log-entry rates,

and the inclusion of a lagged treatment effect

Inclusion of the Inclusion of the Inclusion of alog-entry rate in t log-entry rate in t-1 lagged treatment effect

EZ treatment effect .030** .034*** .036**(.013) (.015) (.014)

Lagged treatment effect -.012(.015)

Log-entry rate .111*** -.051(.027) (.032)

Propensity score -.008* -.011** -.008*(.004) (.005) (.004)

Nb observations 1628 1480 1628

Note: ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.

Year dummies are included and are not reported here. We only keep semesters between 1 and 12. Estimation

method: FGLS with a constant within-municipality unrestricted covariance matrix. The entry rate is defined as

the ratio between the number of entries during the semester and the number of unemployed workers at risk at

the beginning of the semester.

60

Table 15: The effect of treatment on the logarithm of entry and exit rates

Entry rate Exit rate Exit rate Exit rateinto unemployment to job to non-employment to unknown

EZ treatment effect .011 .040*** .039 .013(.021) (.015) (.024) (.014)

Propensity score -.077*** -.009*** -.007* .001(.018) (.003) (.004) (.004)

Nb observations 1628 1628 1628 1628

Note: ***: significant at 1% level; **: significant at 5% level; *: significant at 10% level.

Year dummies are included and are not reported here. We only keep semesters between 1 and 12. Estimation

method: FGLS with a constant within-municipality unrestricted covariance matrix. The entry (resp. exit) rate is

defined as the ratio between the number of entries (resp. exits) during the semester and the number of unemployed

workers at risk at the beginning of the semester.

61

Figure 1: Unemployment rate, entry rate into unemployment and exit rate from unemployment(2nd semester of 1993 - 1st semester of 2003)

.6.6

5.7

.75

.06

.07

.08

.09

.1

1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19Semester

Unemployment rate (left axis) Exit rate (right axis)Entry rate (right axis)

Note: Semester 1 refers to the second semester of 1993. For the entry rate, we represent the average of the current

semester and the following semester to smooth the curve and avoid seasonality effects.

Figure 2: Exit rate to job, non-employment and for unknown reasons

.1.2

.3.4

1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20Semester

Job Non−employmentUnknown

Note: Semester 1 refers to the second semester of 1993.

62

Figure 3: Exit rates to job, by group of municipalities

.08

.1.1

2.1

4.1

6.1

8.2

Exit

rate

to jo

b

1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20Semester

Non−EZ, 8,000−100,000 Enterprise Zones

Non−EZ, 0−5 km Non−EZ, 5−10 km

Note: Semester 1 refers to the second semester of 1993. Non-EZ: municipalities which do not include an EZ.

8,000-100,000: population between 8,000 and 100,000 in 1990. 0-Xkm: between 0 and Xkm of a municipality

including an EZ. Enterprise zones: municipalities which include an EZ.

Figure 4: Exit rates to non-employment, by group of municipalities

.08

.1.1

2.1

4.1

6.1

8.2

Exit

rate

to n

on−e

mlo

ymen

t

1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20Semester

Non−EZ, 8,000−100,000 Enterprise Zones

Non−EZ, 0−5 km Non−EZ, 5−10 km

Note: Semester 1 refers to the second semester of 1993. Non-EZ: municipalities which do not include an EZ.

8,000-100,000: population between 8,000 and 100,000 in 1990. 0-Xkm: between 0 and Xkm of a municipality

including an EZ. Enterprise zones: municipalities which include an EZ.

63

Figure 5: Rates of exit for unknown reason, by group of municipalities

.3.3

5.4

.45

.5Ex

it ra

te to

unk

now

n

1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20Semester

Non−EZ, 8,000−100,000 Enterprise Zones

Non−EZ, 0−5 km Non−EZ, 5−10 km

Note: Semester 1 refers to the second semester of 1993. Non-EZ: municipalities which do not include an EZ.

8,000-100,000: population between 8,000 and 100,000 in 1990. 0-Xkm: between 0 and Xkm of a municipality

including an EZ. Enterprise zones: municipalities which include an EZ.

Figure 6: Exit rate to job, by proportion of EZ population within the municipality

.08

.1.1

2.1

4.1

6.1

8.2

Exit

rate

to jo

b

1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20Semester

high−proportion EZ low−proportion EZ

non−EZ, pop. 8,000−100,000

Note: Semester 1 refers to the second semester of 1993. High-proportion EZ (resp. low-proportion EZ): munici-

palities including an EZ which accounts for more (resp. less) than 50% of the population of those municipalities in

1990. Non-EZ: municipalities which do not include an EZ. 8,000-100,000: population between 8,000 and 100,000

in 1990.

64

Figure 7: Semester-specific risk sets

e2 d2

e1

Semester 1 Semester 3Semester 2 Time

Unemployment spell 1

Unemployment spell 2

d1

65